Nivolumab Plus Standard Dose Bevacizumab Versus Nivolumab Plus Low Dose Bevacizumab in GBM: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Nivolumab Plus Standard Dose Bevacizumab Versus Nivolumab Plus Low Dose Bevacizumab in GBM (NCT03452579), a randomized phase 2 study. The primary outcome is Overall Survival at 12 Months (OS-12).

2. Clinical Question

3. Trial Design

This was a randomized, phase 2, open-label, parallel-group study. Randomization means participants were assigned by chance to one of the two treatment groups; the brief summary says participants and doctors could not choose the group. The registry record lists no masking, so the study was not blinded. The groups received nivolumab with either standard-dose or low-dose bevacizumab.

The registry record lists enrollment of 90 participants. The posted outcome results include 45 participants in each group for the primary endpoint and the listed secondary endpoints. The primary outcome was the percentage alive at twelve months after beginning therapy. Other posted outcomes include six-month progression-free survival, six-month overall survival, and overall response rate. Additional secondary outcomes are listed, but numerical results for all listed secondary outcomes are not posted in the registry record.

The study start date is 2018-05-21 and the primary completion date is 2020-12-30. The current registry status is active, not recruiting. The sponsor is listed as David Peereboom. These registry entries describe the trial record; they do not establish the reasons for choosing the trial size, the conduct of any interim analyses, or the full statistical plan. Those details are not reported in the registry record.

Because the study was open label, participants and clinicians were not masked to the assigned group according to the registry record. Random allocation can help make groups comparable at baseline, but it does not remove uncertainty in estimates from a limited sample, nor does it prevent all sources of bias. The population included in the primary analysis, and the handling of participants after randomization beyond the stated censoring description, are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival at 12 Months (OS-12), measured over Up to 12 months after beginning therapy.

The primary endpoint is overall survival at 12 months, expressed as the percentage of participants who remained alive for at least twelve months after starting study therapy. It is a binary outcome at a fixed time point: a participant either met the stated survival condition or did not. The registry description says participants without efficacy evaluation data or without survival data were censored at Day 1.

A fixed-time survival percentage gives a direct description of how many participants in each group reached the stated time point alive. It is different from a median survival time or a time-to-event hazard estimate, neither of which is the primary measure. The endpoint also focuses on survival rather than tumor response or progression, which appear among the secondary outcomes.

For the primary outcome, the registry reports 41.1% for nivolumab plus standard-dose bevacizumab, with a 95% confidence interval of 26.1% to 56.1%. For nivolumab plus low-dose bevacizumab, it reports 37.7%, with a 95% confidence interval of 23.1% to 52.4%. These are estimates, not exact descriptions of what would be observed in every similar group. Their uncertainty is relevant to any comparison, particularly because each posted group contains 45 participants.

The registry record does not report the detailed analysis-population definition, how censoring was handled beyond the stated Day 1 rule, or further endpoint-analysis procedures. Those omissions limit how fully the endpoint estimates can be reconstructed or evaluated from the record alone.

7. Results Posted in the Registry

• Nivolumab + Low Dose Bevacizumab: 37.8% (17/45) versus 40.0% (18/45) on control; risk difference -2.2 percentage points (95% CI -22.4 to 17.9), risk ratio 0.94 (0.56–1.59); unadjusted two-proportion z-test p = 0.829.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Progression-Free Survival (PFS) at Six Months

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Nivolumab + Low Dose Bevacizumab: 44.4% (20/45) versus 46.7% (21/45) on control; risk difference -2.2 percentage points (95% CI -22.8 to 18.4), risk ratio 0.95 (0.61–1.50); unadjusted two-proportion z-test p = 0.832.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nivolumab + Low Dose Bevacizumab and the control. The interval gives the range of effects that remain compatible with the data.

Overall Survival (OS)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Nivolumab + Low Dose Bevacizumab: 57.8% (26/45) versus 75.6% (34/45) on control; risk difference -17.8 percentage points (95% CI -36.9 to 1.4), risk ratio 0.76 (0.57–1.03); unadjusted two-proportion z-test p = 0.074.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nivolumab + Low Dose Bevacizumab and the control. The interval gives the range of effects that remain compatible with the data.

Overall Response Rate (ORR)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Nivolumab + Low Dose Bevacizumab: 15.6% (7/45) versus 17.8% (8/45) on control; risk difference -2.2 percentage points (95% CI -17.6 to 13.2), risk ratio 0.88 (0.35–2.21); unadjusted two-proportion z-test p = 0.777.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nivolumab + Low Dose Bevacizumab and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes provide results at other time points and for other measures, including six-month progression-free survival, six-month overall survival, and overall response rate. Across these endpoints, the group estimates do not all have the same magnitude or pattern. This variation is unsurprising because survival, progression, and response are different outcomes, and because the time points differ. The secondary estimates add descriptive context around the primary 12-month survival comparison rather than directly answering the same question.

The secondary results do not overturn or resolve the uncertainty in the primary result. They should be interpreted alongside the primary endpoint, not substituted for it because one secondary estimate appears more striking or has a different p-value. The record lists no reported analyses for these secondary outcomes. It also does not report a multiplicity adjustment or explain which secondary comparisons, if any, were prespecified as confirmatory.

When many outcomes are examined, the chance of seeing an apparently notable result by chance can increase. General statistical explanation: adjustment procedures can be used to account for multiple comparisons, but the choice depends on the planned testing strategy. Without a reported strategy, unadjusted secondary p-values are exploratory signals rather than decisive evidence. The registry record does not provide enough information to determine whether a broader multiplicity plan existed outside the posted record.

Several additional secondary outcomes are listed in the registry, but numerical results for all listed outcomes are not reported in the registry record. The missing posted results limit the ability to review the full set of intended outcome measures. Overall, the secondary information is best treated as supportive description with substantial caution, while the primary endpoint remains the main registered comparison assessed.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Progression-Free Survival (PFS) at Six Months
• Overall Survival (OS)
• Overall Survival (OS)
• Overall Response Rate (ORR)
• Progression-Free Survival
• Duration of Response

9. Statistical Interpretation

10. Statistical Methods Explained

What is being compared?

The primary outcome is a percentage of participants who remained alive for at least twelve months after beginning therapy. For each group, the registry gives an outcome estimate and a 95% confidence interval. A confidence interval describes statistical uncertainty around an estimated quantity under the assumptions of the method. It is not a guarantee that the true value lies in that particular interval, and it does not describe the range of individual participant outcomes.

The comparison is a risk difference, with the low-dose group contrasted against the standard-dose group. A risk difference is the difference between the two groups' proportions with the outcome, using the stated order of comparison. A value below zero means the estimated proportion in the low-dose group is lower than the estimated proportion in the standard-dose group; a value above zero means it is higher. The primary estimate is -0.022. Its interval, -0.224 to 0.179, includes zero, which represents no difference in the proportions under this measure.

How should the p-value be read?

The posted unadjusted p-value for the primary comparison is 0.829. In general, a p-value measures how incompatible the observed data are with a specified null model, if that model and the analysis assumptions hold. It is not the probability that the null hypothesis is true, nor the probability that chance alone caused the findings. The registry does not report an adjusted analysis for this result. The p-value should therefore be read as an unadjusted statistic, alongside the effect estimate and confidence interval rather than on its own.

The sample-size illustration states that its planning calculations use a two-sided significance level of 0.05, equal allocation, and a normal approximation. Those are assumptions for the planning illustration, not a reported description of the trial's original design or primary analysis. The original design assumptions and the full analysis plan are not reported in the registry record.

What can the arm estimates say?

The estimates for each group summarize the proportion meeting the endpoint in that group. The displayed percentages and intervals do not by themselves account for every possible source of bias or missing information. The endpoint description says that participants without efficacy evaluation data or survival data were censored at Day 1, but further details about the analysis population and censoring approach are not reported in the registry record. This matters because a reader cannot assess from the record alone how much missing outcome information there was or how it was handled beyond that statement.

The outcome is recorded at a fixed survival time, while some secondary outcomes concern progression-free survival or overall survival at other time points. These are distinct endpoints and need not have the same statistical behavior. A time-point percentage should not be interpreted as a median survival time or a hazard ratio. No such primary measures are posted for this comparison.

Why does over-dispersion matter in general?

General statistical explanation: when outcome variability is greater than a model assumes, standard errors can be underestimated and confidence intervals can be too narrow. This issue is often discussed for count outcomes or clustered data. The primary outcome is reported as a percentage, and the registry does not report a model or variance adjustment that would allow an assessment of over-dispersion. It is therefore not appropriate to claim that over-dispersion occurred or that a particular correction was used.

What is reported about analysis conduct?

The record lists zero reported analyses for the primary outcome and no reported analyses for the listed secondary outcomes. The posted comparison figures include an unadjusted risk difference and p-value, but the registry does not provide a detailed statistical analysis plan, a prespecified hypothesis, interim-analysis details, or adjustment procedures. The record also does not specify an analysis population by a named principle such as intention-to-treat or per-protocol. These details are not reported in the registry record.

As a result, the posted data support a descriptive reading of the group estimates and the stated unadjusted comparison. They do not permit a complete audit of every analysis decision, including endpoint handling, missing-data assumptions, or any planned multiplicity strategy. General statistical concepts can help explain the displayed measures, but they cannot fill those record-level gaps.

11. Confidence Intervals and Precision

The primary endpoint estimates have 95% confidence intervals that extend from 26.1% to 56.1% for standard-dose bevacizumab and from 23.1% to 52.4% for low-dose bevacizumab. Both intervals cover a broad range of possible underlying survival percentages. This indicates that the group-specific estimates are not highly precise in the sense of being tightly bounded.

The comparison interval for the risk difference is -0.224 to 0.179. It includes zero and permits differences in either direction. The estimate itself, -0.022, is near zero, but the interval shows that the data do not narrowly pin down the size or direction of the difference. The interval is the key context for understanding how much uncertainty remains; the point estimate alone can obscure that uncertainty.

Each group has 45 participants in the posted primary results. With this group size, percentages and comparisons can be sensitive to a small number of outcome classifications. The confidence intervals quantify sampling uncertainty under the analysis method, but they do not capture all possible uncertainties, such as bias from open-label conduct, limitations in outcome ascertainment, or missing-data assumptions.

The registry reports 95% confidence intervals for the primary estimates and their comparison. It does not describe the interval calculation method or provide additional sensitivity analyses. Thus, precision can be discussed from the posted bounds, while a full evaluation of the assumptions behind those bounds is not possible from the registry record alone.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size illustration translates the observed comparison into planning scenarios. Its rows represent planning for 100%, 75%, and 50% of the observed effect. The columns give participants per arm for 80% power and participants per arm for 90% power. These are planning quantities, not observed participant counts and not a claim about the power achieved by this trial.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial's own sample-size justification and design assumptions are not reported in the registry record. For the binary outcomes in this trial, the figures refer to participants per arm, rather than total events.

In general, power is the chance that a planned analysis will detect an effect of a specified size under the planning assumptions, if that effect is present. The 80% and 90% columns therefore show different planning targets: the 90% target aims for a higher chance of detecting the chosen effect, which generally requires more participants. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants.

The illustration uses the observed effect as an input, so the resulting values should not be read as a retrospective assessment of the trial's actual ability to detect its effect. They are planning illustrations and not observed power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.400; treatment proportion p₁ = 0.378; average p̄ = 0.389.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6894 = 1.3513.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6892 = 0.5801.
4. n = (1.3513 + 0.5801)² / (-0.0222)² = 7,553.4, rounded up to 7,554 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.4                          # control proportion
p1 <- 0.377777777777778                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3452579)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 7,554 (80% power), 10,112 (90% power)
 75% of observed effect: n per arm = 13,464 (80% power), 18,024 (90% power)
 50% of observed effect: n per arm = 30,371 (80% power), 40,657 (90% power)
power.prop.test: 7553.4 
Simulated power at n = 7,554 per arm: 0.801 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists several secondary outcomes, but it does not report a multiplicity strategy for testing the primary and secondary outcomes together. It also lists no reported analyses for the primary or secondary outcomes. Consequently, it is not possible to determine from the record whether the primary test was intended to stand alone, how secondary hypotheses were prioritized, or whether any adjustment for multiple comparisons was planned or applied.

Multiplicity matters because the interpretation of a collection of tests differs from the interpretation of one prespecified test. General statistical explanation: when multiple hypotheses are tested, unadjusted p-values can make chance findings more likely across the set. A suitable adjustment or a clearly stated exploratory framing can address that issue, but the registry record does not describe either approach. Secondary results should therefore be viewed cautiously and should not be treated as confirmatory solely because a particular estimate or p-value attracts attention.

The endpoint description states that participants without efficacy evaluation data or without survival data were censored at Day 1. It does not report the number of participants affected, the reasons for missing data, or further details of the censoring analysis. The primary analysis population is not specified, and the record does not name an intention-to-treat, per-protocol, or other analysis principle. These details are not reported in the registry record.

The registry also does not provide details of interim analyses, stopping rules, protocol deviations, or sensitivity analyses for missing data. It is not possible to infer that these procedures did or did not occur. Their status is not reported in the registry record. These gaps matter because analysis populations, outcome availability, and repeated testing can affect how estimates and uncertainty should be understood.

For these reasons, the posted primary comparison can be described as an unadjusted comparison with the stated confidence interval and p-value, while the broader analysis framework remains incompletely documented in the registry record.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: generalized muscle weakness (15.6%), fatigue (13.3%), other neurologic (11.1%), hypertension (8.9%), cognitive (8.9%).

The registry reports serious adverse events among 25 of 45 participants in the standard-dose group and 21 of 45 in the low-dose group. It reports other adverse events among 45 of 45 and 44 of 45 participants, respectively. Deaths are listed for 37 participants in the standard-dose group and 40 in the low-dose group. These are separate event counts as posted; the record does not define further how the categories relate to one another.

The listed serious adverse event terms include generalized muscle weakness (15.6%), fatigue (13.3%), other neurologic (11.1%), hypertension (8.9%), cognitive (8.9%), and deep vein thrombosis (6.7%). The registry summary does not identify these term percentages by treatment group, so they should not be assigned to either group from the available record.

These figures are descriptive. The record does not provide a statistical comparison of adverse-event rates, attribution to study treatment, severity grades for each term, or a detailed account of how events were collected. The counts alone do not establish why an event occurred or support a causal comparison between groups.

16. What the Result Does, and Does Not, Mean

The posted primary outcome describes the percentage of participants in each randomized group who were reported to remain alive for at least twelve months after therapy began. The point estimates are close, while the confidence interval for the between-group risk difference is wide and includes zero. This means the posted data leave considerable uncertainty about the direction and size of any difference in this endpoint.

The result does not establish that the two treatment strategies produce the same outcome. Demonstrating equivalence would require a prespecified equivalence margin and an analysis designed for that purpose; neither is reported in the registry record. A non-small p-value is not proof of no difference. At the same time, the estimates do not establish a reliable advantage for either group. The interval includes possibilities in both directions.

The study compares two combinations that both include nivolumab and differ in the bevacizumab dose. It does not compare nivolumab with no nivolumab, or bevacizumab with no bevacizumab. The findings therefore should not be generalized to those untested contrasts based on this trial record.

The trial is listed as phase 2, with 45 participants per group in the posted outcome results. The record does not provide the original sample-size rationale, a full statistical plan, or a detailed analysis-population definition. Those omissions constrain interpretation of both the point estimate and the inferential statistics. The open-label design is also relevant context, particularly for outcomes involving assessment or reporting, although the registry does not establish that it changed any specific result.

In practical statistical terms, these data are a limited estimate of the stated fixed-time outcome in this trial population. They do not by themselves settle comparative effectiveness, explain differences in adverse events, or establish a broader treatment conclusion. Any interpretation should remain anchored to the endpoint, groups, and uncertainty actually recorded.

17. Why This Trial Matters Statistically

This trial is statistically informative because it presents a randomized comparison in which nivolumab was used in both groups and the bevacizumab dose differed. That design makes the primary comparison specifically about the two recorded combination strategies, rather than about whether either drug was used at all. Clear attention to the contrast being estimated is essential when reading comparative results.

The primary outcome is a fixed-time survival percentage, while the registry also lists outcomes based on progression, survival at another time point, and response. These outcomes answer related but distinct questions. The trial illustrates why estimates from different endpoints should not be collapsed into a single impression, and why the registered primary endpoint should remain central to the interpretation.

The uncertainty around the primary comparison is also important. A point estimate near zero can appear reassuringly precise if read alone, but the confidence interval spans a substantial range in both directions. Reporting the interval alongside the estimate prevents the p-value or a rounded percentage from carrying more weight than the data support.

Finally, the record illustrates the value of complete statistical reporting. The posted results include group estimates, confidence intervals, and unadjusted comparisons, but omit the original sample-size rationale, a detailed analysis plan, multiplicity procedures, and key analysis-population details. Such information helps readers understand how confirmatory the analyses were intended to be and how missing outcomes or repeated testing were handled. Without it, the most defensible reading is descriptive and bounded by the posted estimates.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not define the primary analysis population or report how many participants had missing efficacy or survival information. It states that participants without such data were censored at Day 1, but gives no further detail about the handling of censoring. This limits assessment of the endpoint construction and the possible impact of missing information.

The study is open label, with no masking listed. The registry does not report whether outcome assessment was blinded or whether assessment procedures differed between groups. It is not possible to determine from the record whether open-label conduct affected outcome measurement, but it remains a design feature relevant to interpreting assessed outcomes.

The posted primary and secondary comparisons are unadjusted, and a multiplicity plan is not reported. Several secondary outcomes are listed, but numerical results are not posted for all of them. The record also does not report the original sample-size justification, detailed statistical methods, interim analyses, or sensitivity analyses. These absences reduce the ability to evaluate the intended inferential framework.

The primary outcome is reported as a fixed-time percentage with a confidence interval. The record does not provide a hazard ratio or median survival estimate for this primary comparison. It therefore supports interpretation of the stated 12-month outcome, but not reconstruction of a broader time-to-event analysis from the posted figures.

The registry status is active, not recruiting, and the listed primary completion date is 2020-12-30. The record does not explain the relationship between that date and the current status. No explanation should be inferred from those entries alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Nivolumab Plus Standard Dose Bevacizumab Versus Nivolumab Plus Low Dose Bevacizumab in GBM — NCT03452579.
• Registry record last updated 2025-02-28; status last verified 2025-02.
• Results first posted 2025-01-13.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT03452579 is a randomized, open-label, parallel-group phase 2 study in glioblastoma. It compares nivolumab plus standard-dose bevacizumab with nivolumab plus low-dose bevacizumab. The registry lists enrollment of 90 participants, and the posted primary results include 45 participants in each group.

The primary endpoint is overall survival at 12 months. The registry reports estimates of 41.1% and 37.7%, with a low-dose versus standard-dose risk difference of -0.022 (95% confidence interval -0.224 to 0.179; unadjusted p = 0.829). The interval includes zero and leaves substantial uncertainty about the direction and size of a difference.

Secondary results and adverse-event counts add context, but the registry does not report a complete analysis plan, multiplicity procedures, or several details about analysis populations and missing data. The posted findings therefore support a cautious, descriptive interpretation of the recorded outcomes.